Lobbying, Procurement Allocation, and the. Employment Effect of Fiscal Stimulus

Transcription

1 Lobbying, Procurement Allocation, and the Employment Effect of Fiscal Stimulus VERY PRELIMINARY Joonkyu Choi University of Maryland Veronika Penciakova University of Maryland Felipe E. Saffie University of Maryland This Version: February 22, 2017 Abstract We identify the causal effect of lobby behavior on federal procurement allocation during the recent fiscal stimulus period. Using the allocation of contracts under the American Recovery and Reinvestment Act (ARRA) as a laboratory, we show that among firms with a similar propensity to lobby on ARRA in 2009, those firms that actually lobbied on ARRA-related bills won 5% more contracts and 50% larger contracts than firms that did not. We further investigate whether procurement spending channeled through lobbying firms has a differential impact on countylevel employment growth. We find that $1 million procurement spending yields on average of 5.4 jobs, and that the effect is entirely driven by contracts channeled through non-lobbying firms. While procurement channeled through lobbying firms has no significant impact on job creation, $1 million in procurement spending through non-lobbying firms yields 12.3 jobs. Key words: Lobbying, Procurement, Fiscal Stimulus, Fiscal Multiplier, ARRA. 1

2 1 Introduction Fiscal stimulus packages aim to stabilize employment and output during crises, and their effectiveness remains an open question. The enactment of the $831 billion American Recovery and Reinvestment Act (ARRA) in the midst of the Great Recession in February 2009 renewed interest in the impact of stimulus spending. The primary aim of ARRA was to save or create up to 3.5 million jobs, with over 90 percent of those jobs being in the private sector. 1 To date, the literature has primarily focused on the employment effect of aid to state governments (Chodorow-Reich et al. (2012)) and government purchases (Dube et al. (2014), Dupor and Mehkari (2016) Feyrer (2011), Wilson (2012)). We take an additional step forward and ask how stimulus spending was allocated, and whether its impact on employment depends on who it was allocated to. The American Recovery and Reinvestment Act of 2009 provides us with a unique laboratory to explore these questions. We focus on the allocation and impact of one important component of ARRA spending government purchases through federal procurement. Between 2009 and 2014, ARRA-supported federal procurement contracts amounted to $130 billion. Deteriorating economic conditions, combined with this influx of money, may have generated incentives for firms to try to influence the allocation of these contracts. In this paper, we emphasize political influence through lobbying. We know that lobbying firms are active participants in the Federal procurement market. Each year, they account for 1.5% of the 165,000 procurement contractors and 55% of total procurement spending. We therefore ask whether corporate lobbying influenced the allocation of contracts during the crisis; and whether contracts subject to lobby have a differential impact on employment outcomes. To answer the first question we need to identify the causal relationship between lobbying and procurement outcomes. There are several threats to identification. First, in the data it is challenging to link lobbying activity on particular issues with expenditure on particular procurement contracts. Second, lobbying is an endogenous choice made by firms that may be driven by observable (e.g. firm 1 from transcript of President Obama s remarks to Congress on 24 February 2009 ( 2

3 size) and unobservable characteristics (e.g. political connections). Fortunately, ARRA provides a suitable laboratory. In particular, the richness of the procurement and lobbying data allows us to identify both lobbying activity associated with ARRA and the allocation of individual procurement contracts supported by ARRA at the firm level. Additionally, the swift introduction and passage of the stimulus bill assuage concerns regarding lobbying behavior in previous years being targeted toward ARRA contracts these contracts after all did not exist prior to the passage of the bill. In fact, the first version of ARRA was introduced in early January 2009, and was signed into law less than two months later in February. To resolve the challenges associated with selection into lobbying on ARRA, we first prune the sample by matching on a number of observable characteristics. These include firm size, industry, prior lobbying status, and both the number and average size of past procurement contracts. After matching, we obtain 1,061 firms that lobbied on ARRA (treated) matched with 498 similar firms that did not lobby (control). We validate our pruning strategy by ensuring that our resulting treatment and control groups are similar in all observable dimensions and that they have similar pre-arra procurement outcomes. We then assess the impact of lobbying on the allocation of ARRA-supported procurement contracts and find that firms that lobby on ARRA are more likely to win these contracts and win 5.3% more and 50% larger ARRA contracts. This matching approach may not fully capture all the unobserved heterogeneity. For example, even after matching, firms that lobby on ARRA could be more politically connected to the government. In such cases, firms that lobby on ARRA should win more procurement contracts in general, and we might wrongfully attribute this effect to lobby. We validate our identification strategy by showing that ARRA lobbying only has an effect on ARRA procurement outcomes and does not have any significant impact on the corresponding non-arra outcomes. A critical question remains. Did contracts subject to lobbying on ARRA have the same effect on local employment as other procurement contracts? To answer this question we build on the 3

4 rich literature assessing the employment effect of stimulus spending (Chodorow-Reich et al. (2012), Dube et al. (2014), Dupor and Mehkari (2016) Feyrer (2011), Wilson (2012)). To establish causality, we have to address two issues. First, although ARRA procurement spending was fairly dispersed, with 52% of all 3,142 counties receiving contracts, ARRA channeled through lobbying firms was more concentrated. Only 23% of counties received contracts through firms that lobbied on ARRA, which raises a concern about selection since corporate lobbying is endogenous. Second, even after addressing selection, we are concerned with the possibility that total ARRA spending and ARRA spending through lobbying firms are correlated with both employment outcomes and unobserved county-year factors. To address selection, we again prune our sample (Ho et al. (2007) and Stuart (2010)) by matching counties that received positive ARRA procurement through lobbying firms (treated) to those that did not (control) on a large set of observable pre-arra county characteristics including population, employment-to-population ratio, long-run and short-run unemployment trends, industrial and educational composition, and change in the housing price index. We end up with a sample of 342 treated and 230 control counties that we show to be similar in observable dimensions. To address the remaining endogeneity of ARRA spending and ARRA spending through lobbying firms, we construct a set of Bartik instruments. We take advantage of pre-arra (2007) procurement information and aggregate to the countysector level to determine how reliant procurement in each sector is on each county. We assume this reliance is relatively sticky and use it to allocate national ARRA spending in a particular sector across counties. By aggregating over all the sectors within a county, we get an instrument for total ARRA spending. To instrument for the share of procurement spending through lobbying firms, we take advantage of persistence in corporate lobbying Kerr et al. (forthcoming) and variation in the intensity of procurement through lobbying firms across sectors. Over 90% of firms that lobbied on ARRA in 2009 had lobbied on other issues in the previous three years. And while some sectors channel over 80% of total procurement through lobbying firms, others channel as little as 1%. We first calculate the pre-arra (2007) share of procurement spending in each sector channeled 4

5 through firms that lobbied on budget and appropriation. This share is then combined with our county-sector reliance measure and national sector-level ARRA spending. The resulting countysector estimate of ARRA spending through lobbying firms is aggregated to the county level to obtain our second instrument. After pruning and constructing our instruments, we first estimate that ARRA procurement spending yields 5.4 jobs per $1 million spent. This estimate are broadly consistent with, though lower than, the fiscal multiplier reported in Dube et al. (2014) who reports 7.5 job-years created per $1 million spent, or Wilson (2012) who reports eight jobs. 2 We then disaggregate total ARRA procurement per capita into the amount channeled through firms that lobbied on ARRA and those that did not. We find a striking result. The effect of ARRA procurement spending on employment is entirely driven by non-lobbying firms. Stimulus money channeled through these firms yields 12.3 jobs per $1 million spent, while money channeled through lobbying firms has no effect on employment. Although this estimate does not take into account general equilibrium effects, it does suggest that the impact of stimulus spending on employment is attenuated by the allocation of contracts to lobbying firms. In short, it is not only the amount, but also the allocation of stimulus spending across firms that matter for employment outcomes. The paper is organized as follows. Section 2 reviews the related literature. Section 3 describes the goals and characteristics of the American Recovery and Reinvestment Act. Section 4 describes the construction of the data. Section 5 discusses the impact of lobbying on procurement allocation. Section 6 documents the differential effects of ARRA on employment. Finally, section 7 concludes. 2 Literature Review This paper belongs at the intersection of three strands of literature. First, we contribute to the empirical literature evaluating the effectiveness of stimulus spending. The recent literature 2 Our lower estimate is likely driven by the fact that we consider a subset of total government purchases under ARRA, while Dube et al. (2014) and Wilson (2012) consider grants and loans in additional to Federal procurement. 5

6 in this area has focused primarily on ARRA. Some consider the bill s provisions regarding aid to state governments (Chodorow-Reich et al. (2012); Wilson (2012)), while others emphasize the provisions for low-income households, infrastructure spending (Feyrer (2011)), and total government purchases (Dube et al. (2014), Dupor and Mehkari (2016) Wilson (2012)). This strand of literature is principally concerned with estimating the local employment multiplier. Dube et al. (2014) estimate an annualized employment multiplier of 7.5 job-years per $1 million, which is close to the eight jobs estimated by Wilson (2012). Meanwhile, Dupor and Mehkari (2016) estimates that ARRA increases local employment by 9.53 persons at the commuting zone level. We use insights from these papers regarding the regression framework and appropriate controls to ensure that our approach and results are comparable to previous work. We contribute to this literature by focusing on an understudied, yet important, category of government purchases during stimulus Federal procurement. More importantly, we emphasize the differential effect of spending through lobbying and non-lobbying firms on local employment outcomes. Our focus on whether and how lobbying affects the allocation of procurement spending connects us to the large literature investigating various mechanisms through which procurement spending is allocated to firms. The empirical literature on public procurement examines the factors that shape competitiveness and contractual terms (Bajari and Tadelis (2001); Warren (2014); Bajari et al. (2008)), and how different designs of procurement processes affect their efficient allocation outcomes (see Bhattacharya and Sweeting (2015) for a review). Further, Liebman and Mahoney (2013) show that wasteful year-end fiscal spending leads to inefficient procurement allocation in general. In contrast to these studies, we examine lobbying as a determinant of procurement allocation. Finally, our emphasis on the effect of corporate lobbying on the allocation and real effects of procurement contracts during the stimulus closely connects us to the broader literature on the implications of corporate lobbying. This literature has primarily focused on preferential tax treatment (Richter et al. (2009); Meade and Li (2015); Arayavechkit et al. (2014)) and trade policy (Gawande and Bandyopadhyay (2000); Bombardini (2008); Bombardini and Trebbi (2012)). Lobbying has also been found to increase the likelihood of receiving government relief (Duchin and 6

7 Sosyura (2012); Blau et al. (2013); Adelino and Dinc (2014)) and to generate high returns when policies are enacted (Kang (2015)). With the exceptions of Brogaard et al. (2016) and Adelino and Dinc (2014), little has been done to explore how corporate lobbying affects the allocation of procurement contracts. Whereas Brogaard et al. (2016) identifies the positive effect of corporate political connections on the allocation of procurement contracts by exploiting campaign contributions (PAC) in close elections, we use corporate lobbying. The use of lobbying affords us two advantages. i) Corporate lobbying expenditure is seven times larger than corporate campaign contributions, and ii) we can directly link lobby expenditure to particular bills. Adelino and Dinc (2014) document a positive correlation between lobbying and the receipt of ARRA stimulus funds. But, by linking of ARRArelated lobbying and ARRA-related procurement and correcting for selection bias, we can take a further step and establish the causal link between lobbying and the allocation of procurement contracts. 3 The American Recovery and Reinvestment Act To assess the impact of political influence on the allocation and employment effect of procurement contracts during periods of fiscal stimulus, we consider the passage of the American Recovery and Reinvestment Act. ARRA was passed in February 2009 in response to the Great Recession with a stated goal of stabilizing the economy and saving jobs through temporary relief programs, federal tax incentives, and government purchases. Of the estimated $831 billion to be spent beginning in 2009, 31% was allocated to loans, grants, and procurement for infrastructure, energy, communications and scientific research. In total between 2009 and 2014, approximately $130 billion was allocated towards federal procurement. The majority of this contracting occurred between 2009 and As figure 1 shows, by the end of 2010, 61% ($79 billion) of contract dollars had been spent. ARRA was first introduced in the Senate on January 6, 2009 and in the House (H.R. 1 of 7

8 $ Billion Notes: This figure shows the total spending on ARRA supported procurement between 2009 and It The totals include initial obligations, as well as follow-up contract modifications. Figure 1: Arra Contracts: Spending by Year ( ) the 111th Congress) on January 26. It was signed into law by President Obama on February 17. The swift introduction and passage of ARRA reduce the likelihood that firms changed their behavior in anticipation of receiving ARRA supported contracts, which would bias our empirical results. ARRA s $831 billion price tag made it the largest single stimulus bill in U.S. history and efforts were made to monitor spending. In particular, legislation required that all awards funded by ARRA be reported on quarterly and that these reports be made public. Our empirical strategy takes advantage of this publicly available information to identify which procurement contracts are specifically associated with ARRA. We can then integrate publicly available information on lobbying to identify procurement contractors that specifically lobbied on ARRA. Our ability to both identify ARRA procurement and ARRA lobbying allows us to more tightly isolate how political influence, 8

9 exerted through corporate lobbying, affects the allocation and local employment impact of federal procurement during the stimulus. 4 Data Description Our empirical analysis relies on several sources. Federal procurement data is obtained from USAspending.gov, a website mandated by the Federal Funding Accountability and Transparency Act of This site hosts data on the universe of federal procurement contracts awarded since 2000, with size above $3,000 ($25,000 prior to 2005). The data include detailed information on the contracts such as contract size, terms, awarding agency, the location of performance, and product/service type. Additionally, it provides information on the recipient including business name, location, and employment. Among all the contracts awarded, we identify the ARRA-supported contracts using the Recovery Report data from the Federal Procurement Data System (FPDS). Section 1512 of the ARRA requires that recipients of ARRA resources report certain information such as the amount of recovery funds received and a list of projects for which funds will be used. Further, government agencies are required to review the Recovery Report posted on the FPDS website every day to ensure that all entries are accurate. We match the USAspending.gov data and Recovery Report to identify ARRA supported contracts among all procurement contracts. Linking ARRA contracts to the universe of federal procurement contracts is central to our empirical strategy. By doing so, in our firm-level analysis we can control for past procurement experience, and in our county-level analysis we can use pre-arra procurement to construct our Bartik instruments. The federal procurement data are used to construct several outcome variables of interest. For our firm-level analysis we construct a dummy equal to one if the contract is associated with ARRA (DARRA), total number of ARRA contracts (N arra), total first-year value of ARRA contracts (V arra), total number of non-arra contracts (N nonarra), and total first-year value of non-arra contracts (V nonarra). When validating our matching strategy we also use the 9

10 fraction of contracts awarded competitively (COM P ), where competitive contracts are defined as those classified as being awarded under full and open competition. We also construct key control variables: log average first-year value of new contracts in the previous three years (M P 3) and log total number of new contracts won in the previous three years (NP 3), employment (EMP ), and 2-digit industry (N AICS). Because our employment data is derived from reports filed by contracting firms, which is not as reliable as employment from administrative records, rather than use a continuous measure of employment, we place firms into four bins. The first bin contains firms with less than 50 employees, the second with 50 to 249 employees, the third with 250 to 999 employees and the fourth with 1,000 or more employees. For our county-level analysis, we use the data to construct aggregate measures of procurement. Since we are interested in identifying the impact of spending on local employment outcomes, we focus on the location of performance, rather than the location of firms. Doing so better captures the actual location of the plant performing the contract. Further, we measure spending as the sum of all spending obligations, which include initial contract value along with all subsequent contract modifications. 3 We calculate total ARRA spending by county and three-digit NAICs sector (ARRA), as well as total ARRA spending channeled through firms that lobbied on ARRA (ALOB). Our Bartik instruments are built using pre-arra procurement information. At the national level, we measure the share of 2007 procurement spending in each sector going to each county (P rocshare), as well as the total share of 2007 procurement spending in each sector channeled through firms that lobbied on budget and appropriations in 2006 or 2007 (BLOB). Lobbying data is obtained from the Center for Responsive Politics (CRP). The Lobbying Disclosure Act of 1995 requires the disclosure of lobbying activity to the Clerk of the U.S. House of Representatives and Secretary of the U.S. Senate when expenditure exceeds $3,000 during a quarter. In addition to the total amount of expenditure, disclosures also report which issue areas and bills were targeted in lobbying efforts. The data also include the name of organizations or firms on behalf of which lobbying is done. We use this information and a probabilistic name matching 3 Contract modifications involve additional work, changes in costs, termination, etc. We do not distinguish between the type of modification when calculating spending. 10

11 algorithm to link lobby data to federal procurement data. In particular, we first standardize names in the procurement and lobbying data to eliminate punctuation, legal form information, and make adjustments for common acronyms. The names in each data set are further processed to generate match-codes. The procurement and lobby data are then matched based on these codes. More often than not, each entity in the procurement data will at first be matched to multiple entities in the lobby data. We use a Jaro-Winkler distance score to evaluate matches and for each firm keep the match with the highest score. Among the remaining matches, those with a low score are also dropped. We end up finding approximately 4.4% of contractors in the lobby data, and conversely, contractors account for nearly 30% of lobbying entities during the period 2005 through In our empirical analysis we use two variables derived from the lobbying data. The first is a time-varying dummy equal to one if a firm lobbied on any issue in the previous three years (LP 3) and the second is a time-invariant dummy equal to one if a firm lobbied on ARRA in 2009 (F ARRA). We identify a firm as lobbying on ARRA if during the 111th Congress it lobbied on any of the House or Senate versions of ARRA, or related bills (H.R.1, H.R.861, H.R.679, H.R.598, S.1, S.336, and S.350). Lobbying on these bills is identified in the cleaned bill-level data available from CRP and through a string search for the American Recovery and Reinvestment Act and ARRA in the raw disclosure data. 4. For our county-level analysis we incorporate additional data sources to generate control variables previously emphasized in the literature. Our measure of annual working age population ( ) is obtained from the U.S. Census Bureau. County-level quarterly employment information is obtained from the Quarterly Census of Employment and Wages (QCEW) hosted by the Bureau of Labor Statistics (BLS). Using this information we calculate the employment to population ratio ( EMP ). QCEW also provides estimates of the employment share in construction (SCON) and manufacturing (SMANU). We further obtain the housing price index (HP I) from the Federal 4 Our results are robust to a stricter definition wherein the dummy is only equal to one if the firm lobbied on H.R.1 or S.1 during the 111th Congress 11

12 Housing and Finance Agency (FHFA), the share of less-educated young men (SLM E) from the American Community Survey (ACS), and unemployment statistics (U N EM P ) from the BLS. 5 Lobbying and ARRA Procurement 5.1 Descriptive Statistics Before formally identifying the causal impact of ARRA lobbying on the allocation of ARRA contracts, let us explore what the raw data suggest about this relationship. The lobbying data show that the American Recovery and Reconstruction Act attracted significant attention from lobbying firms. In fact, in 2009, approximately $2.4 billion were spent on lobbying and ARRA-related lobby alone accounted for around 7% of the total expenditure. 5 A significant fraction of the entities lobbying to shape ARRA were firms active in the procurement market. Among the 2,100 entities (e.g. foreign governments, associations of firms, associations of consumers, public entities, and companies) 860 (41%) are procurement contractors. These contractors account for two-thirds of all ARRA lobbying expenditure. Nevertheless, lobbying on ARRA-related bills does not guarantee that firms win ARRA contracts. For instance, among the contractors that lobbied on ARRA, approximately 25% were awarded at least one ARRA contract between 2009 and Yet, the returns to winning contracts were likely quite high. Figure 2 compares the size distribution of the average ARRA and non-arra contract awarded to firms, where size is measured as the first year dollar value of a contract. To be clear, if a firm has two ARRA contracts and three non-arra contracts, the average first-year value of the first two contracts is used to build the distribution of ARRA contracts and the average of the other three for the non-arra contracts. Every firm in the procurement database with active contracts is used to generate this figure. Interestingly, the average ARRA contract awarded to firms is on average larger than the average non-arra contract awarded to firms. In fact, the average size of an ARRA contract is nearly $1.6 5 Lobbying disclosure requirements do not require firms to report expenditure separately for each bill. As is standard in this literature, we divide expenditure equally across all bills listed in each disclosure. As such, we anticipate that the ARRA lobby expenditure reported here is a lower bound. 12

13 million compared to $250,000 for non-arra contracts. Density log(real first year contract value) ARRA Not ARRA Notes: This figure shows distribution of log mean first-year contract value for ARRA and non-arra contracts at the firm level between 2009 and The figure excludes observations with zero contract value. Figure 2: Distribution of first-year value: ARRA & Non-ARRA contracts ( ) Figure 3 divides the aforementioned size distribution of ARRA contracts between firms that lobbied on ARRA and contractors that did not. Figure 3 suggests that large ARRA contracts are more likely to be awarded to firms that lobbied on ARRA. The average ARRA contract size to non-lobbying firms is $1.3 million compared to $8.6 million to lobbying firms. There is a similar fraction of lobbying and non-lobbying firms receiving small contracts. But, non-lobbying firms are more likely to receive medium-sized contracts, whereas lobbying firms are more likely to receive large contracts. Perhaps most striking is the fact that firms that lobby on ARRA account for around two percent of the total number of firms awarded ARRA contracts. Yet, these firms were awarded 36% of ARRA contracts and 44% of the total ARRA contract spending between 2009 and 13

14 2011. Density log(real first year contract value) Lobby Non Lobby Notes: This figure shows distribution of log mean first-year contract value for ARRA contracts awarded to firms that lobbied and did not lobby on ARRA at the firm level between 2009 and The figure excludes observations with zero contract value. Figure 3: Distribution of average value of ARRA contracts ( ) 5.2 Pooled OLS Specification Our first aim is to assess whether lobbying is causally linked to procurement allocation during the stimulus period. We take advantage of detailed disclosures that identify lobbying related to the American Recovery and Reinvestment Act, along with ARRA s transparency provisions, which allow us to identify procurement contracts related to the stimulus package. ARRA contracting began in 2009 and we therefore restrict our analysis to 2009 onward. Our empirical approach is cross-sectional in nature and compares outcomes of firms that lobbied on ARRA versus those that 14

15 did not. We estimate the following regression: d=6 Y it =α st + βf ARRA i + γ d (D t F ARRA i ) + δ 1 MP 3 it + d=1 (1) δ 2 NP 3 it + δ 3 EMP it + δ 4 LP 3 it + ε it where Y it is our outcome variable of interest and α st captures industry-year fixed effects. MP 3 measures the average first-year value of contracts awarded in the previous three years and NP 3 measures the total number of new contracts awarded in the previous three years. Both control for the fact that firms may be awarded more and larger ARRA and/or non-arra contracts simply because they have experience in handling such contracting volume and size. EM P controls for the correlation between firm size and federal contracting. And LP 3 controls for the possibility that corporate lobbying of any kind, rather than targeted lobbying on ARRA, influences outcomes. The coefficient on β captures the average effect of lobbying on ARRA in 2009 on outcomes over the sample period (F ARRA), while the coefficients on the interaction between year dummies (D t ) and the time-invariant ARRA dummy (F ARRA) capture the extra (if any) effect that lobbying has on outcomes in 2010 through Therefore, the total effect of lobbying on ARRA in 2009 on, for instance, the total number of ARRA contracts awarded in 2010 is the sum of β and γ 1. Given that our working hypothesis is that corporate lobbying influences procurement allocation, we would expect the coefficient of β and possibly (though not necessarily) the coefficients of γ t to be positive and significant for outcome variables associated with ARRA contracting, and insignificant for outcome variables not directly associated with ARRA. Our preliminary results from pooled OLS regressions are reported in Table 1. Consistent with our expectations, we find that lobbying on ARRA is positively associated with obtaining an ARRA contract (column 1), the number of ARRA contracts (column 2) and the total first-year value of these contracts (column 3). Moreover, it appears that on top of its average effect, lobbying on ARRA further increased the chances, number and (marginally) the size 15

16 of ARRA contracts awarded in This is consistent with the fact that the number of contracts awarded rose between 2009 and 2010, and suggests that those firms who lobbied on ARRA in 2009 disproportionately benefited from this increase. The fact that the interaction term turns negative, and at times significant, in later years is intuitive. It suggests that influence of lobbying dies out over time. However, inconsistent with our expectations, is the fact that lobbying on ARRA is also positively correlated with the number of non-arra contracts awarded in the post-2009 period, and somewhat unintuitively is negatively correlated with the total first-year value of non-arra contracts. 16

17 Table 1: Corporate lobbying and procurement allocation (pooled OLS regression) (1) (2) (3) (4) (5) DARRA N ARRA V ARRA N nonarra V nonarra F ARRA (0.0120) (0.0183) (0.176) (0.0333) (0.0871) D 2010 F ARRA (0.0187) (0.0308) (0.265) (0.0471) (0.121) D 2011 F ARRA (0.0164) (0.0262) (0.231) (0.0489) (0.127) D 2012 F ARRA (0.0155) (0.0208) (0.213) (0.0511) (0.127) D 2013 F ARRA (0.0161) (0.0223) (0.213) (0.0537) (0.127) D 2014 F ARRA (0.0166) (0.0225) (0.217) (0.0571) (0.134) D 2015 F ARRA (0.0163) (0.0221) (0.222) (0.0538) (0.131) Ind-Year FE Yes Yes Yes Yes Yes Full Controls Yes Yes Yes Yes Yes Obs. 615, , , , ,988 R-sq Notes: The dependent variable in the first column is a dummy whether the firm was awarded any ARRA contract; in the second column is the number of ARRA contracts awarded; and in the third column is the total first-year value of ARRA contracts. The fourth column is the number of non-arra contracts awarded and the last column is the total first-year value of non-arra contracts. We only report the coefficients of variables of interest, namely the time-invariant dummy F ARRA, which is equal to one if the firm lobbies on ARRA in 2009, and its interaction with time dummies. In all regressions we also control for industry-year fixed effects and for firm-level employment, lobbying in the previous three years, and the average value and total number of new contracts awarded in the previous three years. Standard errors are robust. ***, **, and * indicates significance at the 1%, 5%, and 10% levels, respectively. One important concern regarding the full sample used in our analysis thus far is selection bias. As table 2 shows, well under 1% of all procurement contractors lobby, but those that do 17

18 Table 2: Pre-matching difference between ARRA lobbying and non-lobbying firms Mean Variable ARRA Lobby Non Lobby #F IRM S 1, ,507 EM P LP MP NP Notes: The table reports the comparison of means between treated (ARRA lobby) and untreated (Non Lobby) firms in the unmatched sample for all variables that will be used in our propensity score matching. are quite different from the rest. In particular, they have earned more and larger contracts in the past (NP 3 and MP 3); have virtually all lobbied in the previous three years (LP 3); and have higher employment (EM P ). The average ARRA lobbying firm belongs to the size bin representing employment above 250 and the average non-lobbying firm belongs to the size bin representing employment below 50. Ideally, we would like to know the counter-factual award of ARRA contracts to firms that lobbied on ARRA if they had instead chosen not to lobby. Since such a counter-factual is unobservable, we are forced to rely on a control group of firms that did not lobby on the stimulus bill. Since lobbying is an endogenous choice and correlated with factors such as firm size, which also affect contract allocation, the sample of all firms that did not lobby on ARRA is not an appropriate counter-factual. We address this selection bias by using a standard propensity score matching approach. 5.3 Matching For the results reported in the next section, we restrict ourselves to a sample of firms that lobbied on ARRA in 2009 (treatment group) and a sample that is observationally similar to the treated group but that did not lobby (control group). In the first stage, we focus on the crosssection of firms in 2009 since this is the year in which treatment status is determined. We estimate a logit model to predict whether a firm lobbies on ARRA as a function of all the firm characteristics 18

19 used in the pooled regression, including employment (EM P ), industry (N AICS), lobbying status over the previous three years (LP 3), number of new contracts awarded in the previous three year (NP 3), and the mean value of those contracts (MP 3). Formally, we estimate: F ARRA i = λ s + η 1 MP 3 it + η 2 NP 3 it + η 3 EMP it + η 4 LP 3 it + ε it (2) We then use the resulting propensity scores to construct a nearest-neighbor matched sample of firms. Once we identify our control group in 2009, we track the group from that year onward in our second stage regressions. With this approach we eliminate from our sample procurement contractors that are observationally very different from those firms that lobbied on ARRA in Before turning to our matched sample estimation results, it s helpful to review the results from our first stage in table 3. Because we allow for matching with replacement, our 1,061 firms that lobbied on ARRA are matched to a sample of 498 firms that did not. As a result, our second stage regressions will employment frequency weight. Table 3 confirms that our nearest neighbor matching virtually eliminates selection on observables. Table 3: First-stage: post-estimation comparison Mean Variable Sample ARRA Lobby Non Lobby Bias #F IRM S Unmatched 1, ,507 Matched 1, EM P Unmatched Matched LP 3 Unmatched Matched M P 3 Unmatched Matched N P 3 Unmatched Matched Notes: The table reports the comparison of means between treated (ARRA Lobby) and untreated (Non Lobby) firms in the unmatched and matched sample for all variables used in the first-stage regressions. 19

20 As suggested in Imbens and Rubin (2015), we consider an additional validation exercise. If our matched sample does well in addressing selection, we would expect no differences in pre-arra ( ) procurement outcomes for the treated and control groups. Table 4 considers the total number (NUM), total number of large (NUM50), and total first year value (V AL) of contracts in the first three columns. As should be the case, lobbying on ARRA and its interaction terms have no significant effect on these outcomes. We might be concerned that these outcomes are highly correlated with the procurement related variables used in our first stage. In column (4) we find that for a non-targeted outcome, the share of contracts awarded competitively (COM P ), there is still no statistically significant difference between our treatment and control groups. Table 4: First-stage post-estimation) (1) (2) (3) (4) NUM NUM50 V AL COMP F ARRA (0.116) (0.117) (0.197) (0.0134) D 2007 F ARRA (0.159) (0.160) (0.268) (0.0195) D 2008 F ARRA (0.126) (0.131) (0.236) (0.0196) Ind-Year FE Yes Yes Yes Yes Full Controls Yes Yes Yes Yes Obs. 2,522 2,522 2,522 2,522 Freq. Weighted Yes Yes Yes Yes R-sq Notes: The period of analysis is The dependent variable in the first column total number of contracts; in the second column is total number of contracts above the 50th percentile in first year value; in the third column is total first year value; and in the fourth column is the share of contracts awarded competitively. We only report the coefficients of variables of interest, namely the time-invariant dummy F ARRA, which is equal to one if the firm lobbies on ARRA in 2009, and its interaction with time dummies. In all regressions we also control for industry-year fixed effects and for firm-level employment, lobbying in the previous three years, and the average value and total number of new contracts awarded in the previous three years. Standard errors are robust. ***, **, and * indicates significance at the 1%, 5%, and 10% levels, respectively. 20

21 5.4 Regression Results with Matched Sample The results from our second stage regressions, reported in table 5 show that lobbying is indeed influential in shaping the allocation of ARRA-supported procurement contracts. After controlling for selection into lobby by restricting the analysis to a smaller sample of firms that are similar in size, past lobbying and experience in federal procurement, we still find that firms that lobbied on ARRA in 2009 are on average significantly more likely to win ARRA contracts. Importantly, the magnitudes are economically significant. When the regression is evaluated at the mean, the results imply that firms that lobbied on ARRA-related bills won 5% more and 50% larger ARRA-contracts than firms that did not lobby on ARRA. Although the control group from the matched sample closely resembles the treated group, there is still room for unobserved factors that make firms both lobby more intensively on ARRA and win more contracts. For this reason, we evaluate non-arra contract outcomes of ARRA lobbying and non-lobbying firms. In contrast to the pooled regression approach, once we correct for selection, we find that lobbying on ARRA has not impact on the number or size of non-arra contracts awarded. Because it is unlikely that the unobserved factors differentially affect ARRA and non- ARRA contracts the relationship uncovered in this section between lobbying and procurement is likely to be causal. Because the interaction terms for 2010 and 2011 are positive, we can conclude that the marginal effect of ARRA-related lobbying on ARRA contracting outcomes rises over this period, although not significantly so. Both joint and total significance tests yield significant results for the 2010 and 2011 interaction terms. The fact that the interaction terms turn negative beginning in 2012 is natural. ARRA-supported contracts are very scarce at the end of the sample period and the positive effect of lobbying is likely to wane after a few years. In fact, the total significance of F ARRA and interaction terms in 2012 through 2015 is consistently insignificant. Summarizing, after correcting for selection bias by employing nearest neighbor matching, we find a strong positive effect on the probability, number, and size of ARRA-contracts awarded to 21

22 firms engaged in corporate lobbying on ARRA and the non-causal correlation between ARRA lobbying and non-arra contracting vanishes. Table 5: Corporate lobbying and procurement allocation (Second-stage regression) (1) (2) (3) (4) (5) DARRA N ARRA V ARRA N nonarra V nonarra F ARRA (0.0147) (0.0199) (0.206) (0.0380) (0.126) D 2010 F ARRA (0.0257) (0.0381) (0.350) (0.0569) (0.159) D 2011 F ARRA (0.0210) (0.0340) (0.282) (0.0581) (0.162) D 2012 F ARRA (0.0218) (0.0258) (0.280) (0.0613) (0.166) D 2013 F ARRA (0.0220) (0.0263) (0.275) (0.0638) (0.173) D 2014 F ARRA (0.0229) (0.0276) (0.283) (0.0764) (0.190) D 2015 F ARRA (0.0238) (0.0266) (0.298) (0.0665) (0.193) Ind-Year FE Yes Yes Yes Yes Yes Full Controls Yes Yes Yes Yes Yes Freq. Weighted Yes Yes Yes Yes Yes Obs. 5,929 5,929 5,929 5, R-sq Notes: The table reports results for the matched sample of firms obtained from nearest neighbor matching. The dependent variable in the first column is a dummy whether the firm was awarded any ARRA contract; in the second column is the number of ARRA contracts awarded; and in the third column is the total first-year value of ARRA contracts. The fourth column is the number of non-arra contracts awarded and the last column is the total firstyear value of non-arra contracts. We only report the coefficients of variables of interest, namely the time-invariant dummy F ARRA, which is equal to one if the firm lobbies on ARRA in 2009, and its interaction with time dummies. In all regressions we also control for industry-year fixed effects and for firm-level employment, lobbying in the previous three years, and the average value and total number of new contracts awarded in the previous three years. Standard errors are robust. ***, **, and * indicates significance at the 1%, 5%, and 10% levels, respectively. 22

23 6 Differential Effects of ARRA Procurement on Employment Growth 6.1 Descriptive Statistics Having shown that lobbying effects the allocation of ARRA-supported contracts, we now turn to whether this influence has implications for local employment outcomes. The foundation of our empirical approach is the well-established (Chodorow-Reich et al. (2012), Dube et al. (2014), Dupor and Mehkari (2016) Feyrer (2011), Wilson (2012)) use of geographic variation in stimulus spending to identify the effect of this spending on labor market outcomes. As figure 4 shows, there is quite a bit of variation in ARRA supported federal procurement per capita in 2009 and Spending per capita appears more concentrated in counties on the East and West coasts, with much of the mid- West receiving fewer per capita dollars. This geographic variation helps us achieve identification by asking whether regions that received more money per capita created or saved more jobs , No data Notes: This figure shows the distribution of total ARRA procurement spending per capita across counties between 2009 and Figure 4: Distribution of ARRA Procurement across Counties 23

24 We are interested in whether ARRA spending channeled through firms that lobbied for ARRA contracts has a different effect on employment than ARRA spending channeled through other firms. To identify this effect, we need sufficient geographic variation to ask whether regions that received less money per capita through lobbying firms were able to create or save more jobs. Figure 5 shows the fraction of total ARRA procurement awarded to firms that lobbied on ARRA. While we do find variation, with some areas channeling over two-thirds of their procurement through lobbying firms, there are many counties where this share is zero. Out of 3,142 counties, 1,626 received positive ARRA procurement, but only 371 received ARRA spending through lobbying firms. As a result, we face difficulties in inferring differential employment effects, and are additionally concerned about potential selection bias. As a result, we turn to the approach of Ho et al. (2007) and Stuart (2010), who suggest pre-estimation sample pruning. More specifically, we take the 371 counties receiving positive ARRA spending through lobbying firms and match them on a large set of observables to a sample of firms that did not receive such spending. We then estimate the effects of ARRA spending through different types of firms on employment outcomes using this pruned sample No data Notes: This figure shows the distribution of the share of total ARRA procurement spending channeled through firms that lobbied on ARRA across countries between 2009 and Figure 5: Distribution of Lobbying share of ARRA Procurement across Counties 24

25 6.2 Pre-Estimation Sample Pruning We are interested in estimating the following baseline model: L i,t L i,0 i,0 = β 0 + β 1 NonLob i i,0 + β 2 Lob i i,0 + X i,0δ + γ + ɛ i (3) The dependent variable is change in employment in county i between the fourth quarter of 2008 and the fourth quarter of 2010, scaled by the population of the county in We control for a list of covariates (X i,0 ) that the literature has found to strongly predict changes in employment, particularly during the recent financial crisis. These include the size of the economy as measured by the working-age population in 2008; long-run trends in employment as measured by the change rate in the employment to population ratio in the previous five years; and short-run economic conditions measured by the unemployment rate in We also control for the employment share in manufacturing and construction, which is motivated by Charles et al. (2013) who show that the decline in manufacturing had a large impact on non-employment, and that the boom and bust of housing prices had a causal impact on non-employment among construction workers. We control for the share of young (age 18-24) men with less than a college education to take into account that they exhibited the sharpest decline in the employment-to-population ratio during the crisis. Finally, to account for the fact that the areas experiencing the largest housing boom were also the hardest hit by the financial crisis, we control for the increase in the rate of the housing price index between 2003 and Our two variables of interest are NonLob and Lob, which measure the total amount of ARRA procurement per capita through firms that did not lobby on ARRA and the total amount of ARRA procurement per capita through firms that did lobby, respectively. We are particularly interested in differences between the coefficients β 1 and β 2. Before moving forward with estimating our baseline model, we first need to prune our sample of counties to take case of potential selection into positive ARRA procurement through lobbying firms. 25

26 In order to do so, we use Mahalanobis distance matching on the same set of covariates used in our second stage. We identify as treated the set of counties that received positive ARRA spending through firms that lobbied on ARRA and the control group as those counties that did not. Our pruned sample contains the 342 treated counties and a set of 230 observationally similar control counties In table 6 we see that in our full (unmatched) sample, counties awarding money to firms that lobbied on ARRA tend to be substantially large, and have a higher employment to population ratio, lower manufacturing employment share, and higher housing price index growth between 2003 and After matching our sample of treated and control counties is more similar, but because, as is common, we are unable to eliminate all bias, we will continue to control for the full set of covariates. Table 6: First-stage: post-estimation comparison Mean Variable Sample Treated Control Bias log( 2008 ) Unmatched Matched EMP q Unmatched Matched EMP 5yr Unmatched Matched SM AN U Unmatched Matched SCON Unmatched Matched SLM E Unmatched Matched HP I Unmatched Matched UNEMP 08 Unmatched Matched Notes: The table reports the comparison of means between treated (received positive ARRA through lobbying firms) and untreated (did not receive any ARRA through lobbying firms) counties in the unmatched and matched sample for all variables used in the first-stage regressions. Using this matched sample of counties, we estimate our baseline model first using total ARRA 26

27 procurement spending per capita. Our results in table 7 estimate that every $1 million in procurement spending between 2009 and 2010 created or saved 3.3 jobs. In the second column, we decompose ARRA procurement spending into that channeled through non-lobbying and lobbying firms. The results suggest that the employment-effect of ARRA procurement is entirely driven by contracts awarded to non-lobbying firms. For every $1 million spent through these contractors creates or saves 4.3 jobs. In contrast, procurement through firms that lobbied on ARRA has no significant effect on employment growth between 2008 and Table 7: County Emplyoment Outcomes & ARRA Procurement (Pruned Sample) ARRA NonLOB (1) (2) ( ) EMP ( ) EMP (3.98) (3.20) 0810 LOB (0.96) State FE Yes Yes Full Controls Yes Yes Freq. Weighted Yes Yes Observations R-sq Notes: The table reports results for county-level regressions after sample pruning. The dependent variable is the change in employment-to-working age population ratio between the fourth quarter of 2009 and the fourth quarter of We only report the coefficients of variables of interest, namely total ARRA procurement spending per capita ( ARRA ), total ARRA spending channeled through firms that did not lobby on ARRA ( NonLob ), and total ARRA spending channeled through firms that lobbied on ARRA ( LOB ). In all regressions we also control for state fixed effects, log working age population in 2008, employment to working age population ratio in 2008, prior 5-year average change rate in the employment to population ratio, manufacturing employment share in 2008, construction employment share in 2008, share of low educated young men in 2008, unemployment rate in 2008, and the change rate in the housing price index from 2003 through Standard errors are robust. ***, **, and * indicates significance at the 1%, 5%, and 10% levels, respectively. 27